Zombie ideas in ecology: the local-regional richness relationship (UPDATED)

The local-regional richness zombie is one I’ve mentioned in passing in various posts, but to which I’ve never actually devoted an entire post. It’s time to change that, thanks to the publication of an important new paper by Gonçalves-Souza et al. (forthcoming at Oikos; UPDATE: link fixed).* They’ve just taken a heck of a shot at killing off this zombie.

UPDATE: As a commenter notes, Szava-Kovats et al. (forthcoming at Ecology) was published online two days earlier than Gonçalves-Souza et al. and used the same approach to reach the same conclusions. I was aware of both papers, having reviewed them both, but hadn’t realized that Szava-Kovats et al. had just been published online too. For the record, Gonçalves-Souza et al. was actually accepted by Oikos before Szava-Kovats et al. was submitted. But I really don’t think priority should be the focus here. Certainly, in focusing my post on Gonçalves-Souza et al., I did not mean to try to confer priority on them, and I certainly didn’t mean to slight the equally-fine work of Szava-Kovats et al. The important thing is that both groups, working independently of one another, reached the same conclusions using the same methods. I find that reassuring. It’s not a given that two independent reviews of the same literature will reach the same conclusions. Think of recent competing meta-analyses of the diversity-productivity relationship, or further back the famously somewhat-contrasting reviews of field competition experiments by Schoener 1983 and Connell 1983.

Over at Oikos Blog, Gonçalves-Souza et al. have a fun summary of their paper which flatters me by placing their work within my own zombie-slaying tradition. I assume this is how a superhero feels when first joined by a sidekick. 😉 But after you click through and read their post, come back here and see what I have to say, because I’m going to draw some larger lessons about research programs in ecology and how they can avoid pursuing zombie ideas.

Briefly, the local-regional richness zombie is a shortcut (and you know what I think of those…). The idea is that, by plotting the species richness of local communities against the species richness of the regions in which they’re embedded, you can infer whether local species interactions are strong enough to limit local community membership. Here’s the argument. Species within any local community (a lake, a patch of grassland, whatever) typically didn’t speciate there. Instead, they colonized that local site from somewhere else, presumably from somewhere in the surrounding “region” (the regional “species pool”, if you like). Of course, not all colonists necessarily succeed in establishing a local population. In particular, they might fail because they get competitively excluded by other species. So local species richness reflects both the influence of the surrounding region (the source of colonists), and local conditions that determine the fate of colonists. How can we tease apart the relative importance of regional-scale and local-scale factors in determining local species richness? Why, by going out and sampling the species richness of local communities in different regions, and the richness of those regions, and then regressing local richness on regional richness. If we get a saturating curve (i.e. a curve that asymptotes or seems to be approaching an asymptote), then that means that local communities in sufficiently-rich regions are “saturated” with species.** All the niches are occupied and local competition prevents further colonization, setting an upper limit to local richness no matter how many species there are in the regional “species pool”. Conversely, if the local-regional richness relationship is linear, that means that local competition is too weak to limit local community membership. Instead, local communities are just samples of the regional species pool. Local communities just contain some constant fraction of the species from the surrounding region, with that fraction reflecting colonization rate. Lots of people have tried this idea out in their own systems–including me! (Fox et al. 2000)

Now, I’m sure you can imagine many potential problems with this approach. And you’re right to imagine problems. One big problem is that there are all sorts of confounding factors that will affect the shape of the local-regional richness relationship, but have nothing to do with the strength of local species interactions, colonization rates, etc. Differences among regions in environmental conditions and evolutionary history, to name just two. Another big problem is how to define “local” and “regional” scales, especially when localities and regions lack natural borders. Define either or both scales incorrectly (and how could you tell if you got them right?), and you’ll likely get the wrong answer. A third big problem is that the basic intuition behind this whole approach doesn’t stand up to scrutiny. There’s actually no reason to expect a connection between the processes determining local species richness and the form of the local-regional richness relationship. For instance, you can get linear or saturating local-regional richness relationships from a dead-simple model that lacks any local species interactions whatsoever, just by tweaking model parameters (Fox et al. 2006). For further review of the many obstacles to interpreting local-regional richness relationships the way most people have interpreted them, see Srivastava (2002), Hillebrand (2005), and other recent reviews.

Now, the numerous attacks on local-regional richness relationships as a shortcut to insight haven’t been ignored. But they certainly haven’t caused people to give up on the idea. My experience as a reviewer of many papers on this topic is that the issues reviewed above are acknowledged, but often only at the behest of reviewers, and usually only in passing. Basically, many authors take the view that, while looking at local-regional richness relationships isn’t a perfect way of inferring the determinants of local species richness, no approach is perfect, so we should just push ahead with what we’ve got and see what we find. Authors taking that view find it reassuring that a pattern does seem to emerge: local-regional richness relationships mostly are linear, and that seems to be true no matter what system you study. Indeed, to a certain sort of ecologist, a repeated pattern is in and of itself a strong reason to keep pursuing any research related to that pattern.

Trouble is, the apparent “pattern” is a statistical artifact. There is no pattern. As Gertrude Stein once said of the city of Oakland, “There is no there there.

Let me explain. The standard way to test for linear vs. saturating local-regional richness relationships is to test whether a quadratic regression fits the data better than a linear regression. But the problem with that approach is that the “operational space” for the regression isn’t unbounded. By definition, a local site within a region can’t contain more species than the region. So all local-regional richness relationships, linear or saturating, are constrained to fall below the 1:1 line. Now, if observed local-regional richness data always fell well inside the boundaries of the operational space, maybe the boundedness of the operational space wouldn’t be a problem. But in practice, at least some observed data points in most datasets fall close to or on the boundaries of the operational space.

In a big statistical advance, Szava-Kovats et al. (2011; I handled it as an editor at Oikos) came up with a clever way around this by means of a logratio transformation, so that the regression can be conducted in an unbounded operational space. Now, I wouldn’t necessarily call logratio regression “the” right way to analyze local-regional richness relationships. Bounded operational spaces are tricky to deal with statistically and I don’t think there’s any universal “recipe” for how to deal with them. But I do think logratio regression is a clear improvement over conventional regression here–it gives you more interpretable answers without being any more difficult to implement (statistical machismo, this ain’t). Szava-Kovats et al. applied their new logratio regression approach to a few illustrative examples, showing that it changes the conclusion in some cases.

Now Gonçalves-Souza et al. have taken the next step and gone back through the literature reanalyzing every published local-regional richness relationship they could find using this improved statistical approach. It turns out that the apparent prevalence of linear local-regional richness relationships is an artifact of conducting linear regressions in a bounded operational space. 70% of published local-linear richness relationships look linear when analyzed by conventional regression–but only 53% do when analyzed with a logratio regression, with the other 47% being saturating. Fully 40% (!) of published local-regional richness relationships are misclassified by the conventional regression approach. Indeed, some of the most famous and widely-cited “textbook” examples of “linear” local-regional richness relationships actually are saturating. Which is unfortunate, given that these “textbook” examples literally are in the textbooks!

Now, if you’re attached to local-regional richness relationships as a shortcut to insight into the determinants of local species richness, you might respond by saying something like the following. “Ok, but that just changes the question from explaining a pattern to explaining variation. We need to figure out why about ~50% of studies find linear local-regional richness relationships, and the other ~50% find saturating ones.” Sorry, but Gonçalves-Souza et al. were way ahead of you on that–and it’s a non-starter. They looked at a whole boatload of ecological and methodological covariates: taxonomic group, trophic position, thermoregulation, adult dispersal mode, biogeographic realm, hemisphere, study design, and study scale. They found precisely nothing–none of these covariates explains why some studies find linear local-regional richness relationships while others find saturating ones. As far as we can tell, whether you see a linear or saturating local-regional richness relationship is a coin flip.

I think there are several lessons here.

First, there’s no longer any reason to study local-regional richness relationships. If that seems like an overly-strong conclusion to you, well, let’s review the bidding. Theory says that there all sorts of different processes or combinations of processes that can lead to linear local-regional richness relationships, and that those very same processes or combinations of processes also can lead to saturating relationships, depending on parameter values. So theory basically says “Anything can happen, it depends on a whole bunch of idiosyncratic and system-specific details.” And when we go out in nature and collect data, the results we obtain are almost literally a coin flip, the outcome of which can’t be predicted by any obvious predictor variable. Does this sound to you like a good starting point for further research? The data are a bunch of coin flips, the outcome of which we’re unable to predict, and theory says there’s no reason to expect anything else. Even if you admit that local-regional richness relationships aren’t a shortcut to mechanistic insight, and you just want to study and explain them for their own sake, why would you want to? With all the other actual patterns in the world that you could be studying? And what gives you any reason to think that you’ll be able to make any progress? As I’ve noted before, “Not much is known about X” is actually a reason not to study X!

Second, while I’m not so foolish as to think that the local-regional richness zombie actually has been slain (I’ve learned my lesson on that), I do wonder if Gonçalves-Souza et al. have at least dealt it a body blow. I say that because previous attacks on the local-regional richness relationship were different in character. For instance, mathematical theory is always going to have an uphill battle against people’s pre-theoretical intuitions. And technical issues like defining the boundaries of localities and regions are universal. Those technical issues really are the sorts of issues that need to be recognized, but that shouldn’t be allowed to halt a promising research program. But now Gonçalves-Souza et al. have shown that the existing data do not show what everyone thinks they show, even at a purely descriptive level. Similarly, in economics Paul Krugman wonders if the exposure of clear-cut empirical problems with the claims of Reinhart-Rogoff will undermine the influence of that paper in a way that conceptual and technical criticisms never could (see here for my discussion of Reinhart-Rogoff and its relevance to ecology).***

Third, if you say that, well, local-regional richness relationships were a dead end, but at least they spawned a lot of useful work, I respectfully disagree. Being influential doesn’t compensate for being wrong. Without meaning to be snarky at all or to put down anyone who’s worked on this (all sorts of great ecologists have worked on local-regional richness relationships), I think the following is a fair summary of what we’ve learned: “The local-regional richness relationship is linear about half the time, and saturating about half the time, a fact we can’t explain and from which we can infer nothing.” Going down blind alleys is unavoidable, and there is no shame in it (if we knew what we were going to find, it wouldn’t be research, as the saying goes). Again: this is a blind alley I myself went down at one point! But it’s nothing but unfortunate when we do go down a blind alley. Plus, as noted above, really serious criticisms of local-regional richness relationships as a shortcut to mechanistic insight have been published repeatedly since the late 1990s, and have been repeatedly acknowledged but never resolved. When first proposed as a shortcut, local-regional richness relationships were well worth pursuing. But I think the “shortcut” could’ve been recognized earlier for the blind alley it unfortunately turned out to be. I suspect Brian may disagree with me on this one, as in general he’s a strong advocate for “muddling through” with imperfect approaches in the hopes the future researchers will improve them. But in this specific case, few improvements have been forthcoming, and the methodological advances that we’ve made (such as logratio regression) often have been such as to reinforce rather than solve earlier concerns.

Fourth, I hope nobody tries to argue that we’ve just got to keep on keepin’ on with this research program, somehow building on what’s been done so far rather than just abandoning it, on the grounds that no alternative is available. Because there are plenty of alternatives! In particular, we’ve never been short on ways to test how open local communities are to colonization by species not currently present. Like, say, actually doing experiments to see if local communities are open to colonization by species not currently present. Those experiments aren’t even that difficult in many systems, which is why many such experiments have been done (think of seed sowing experiments to test the invasibility of plant communities, or the classic work of Jon Shurin in zooplankton communities). Similarly, if you want to know if the species within local communities are competing, and how strongly, you can do what a bazillion community ecologists have done and do straightforward removal experiments to find out. I’ve never understood the attraction of local-regional richness relationships as a shortcut to insight about the determinants of local species richness or the strength of local species interactions. In many systems, it’s straightforward to answer those questions via direct experimentation, so why do we need a shortcut here? Why approach those questions via a roundabout, highly-dubious inference from the shape of the local-regional richness relationship? (And don’t say, “Because we need to know if those local processes matter at larger scales”, because what happens at larger scales is just the aggregate outcome of what happens at smaller scales. I’ve discussed this more than once.) More broadly, there are all sorts of ways to study “metacommunities”, or the consequences of community “openness”, or the interplay of processes operating at different spatial scales, or etc. If we just give up on local-regional richness relationships, full stop, we are not going to be short on questions to ask about spatial community ecology, or perfectly-feasible ways of answering those questions! We really can just quit studying local-regional richness relationships without doing any harm to our ability to address any substantive question in ecology.

Local-regional richness relationships were a good idea at the time. Like many good ideas in science, it didn’t pan out. I think we could’ve recognized that earlier, but hey, whatever–the important thing is that we recognize it now. Time to admit that local-regional richness relationships were a dead end, rather than letting this now thoroughly-discredited idea persist as a zombie.

*Full disclosure: I reviewed this paper for Oikos. I’ve been planning to blog about it since I reviewed it, even though I don’t usually blog about new papers, because I think it’s a particularly important paper. But I decided to wait to post until the authors had their own post up on Oikos Blog, because I didn’t want to steal their thunder.

**Anyone else besides me wonder how much of the appeal of local-regional richness relationships as a shortcut is down to the fact that one can use the same word (“saturating” and variations thereon) to both describe a regression that reaches an asymptote, and to describe the ecological processes that putatively give rise to such regressions? This verbal fact has the unfortunate consequence of suggesting that the interpretation of the regression is almost inherent in the regression–almost as if no interpretation at all is required. And indeed, I have occasionally reviewed papers that mix these two things up, talking as if a saturating regression is one and the same thing as local communities that are saturated with species. Choice of words can mislead us in science, and I suspect it has done so in the case of local-regional richness relationships.

***To be clear, I am not saying that conventional analyses of local-regional richness relationships were goofs like Reinhart-Rogoff’s Excel blunder! All I’m saying is that the work of Gonçalves-Souza et al. pushes back against the conventional wisdom about local-regional richness relationships in a different, more empirical way than previous pushback.

Cool forthcoming Oikos papers

Some forthcoming (in press) Oikos papers that caught my eye. Lots of good stuff in the pipeline!*

Nadeem and Lele introduce a new maximum likelihood-based method of population viability analysis (PVA) and test it on song sparrow time series data. The new method, called “data cloning”, was previously developed by Lele in other contexts. It estimates observation error as well as process error (e.g., demographic stochasticity), and deals gracefully with missing data. The clever thing about it is that it has all the computational advantages of more popular Bayesian estimation methods, but it’s fully frequentist and so doesn’t need priors. Which is a good thing because priors for the rare, poorly-known species for which we often want to construct PVAs often are pretty arbitrary guesses which have strong effect on the outcome of the analysis because there’s not enough data to “swamp” them. You also avoid having to adopt the subjectivist Bayesian interpretation of what your probabilities (e.g., extinction probabilities) mean. In the case of song sparrows, it turns out that incorporating observation error into the analysis really changes the results. The approach is even sensitive enough to detect evidence that the data and associated PVA model omit important biological processes (here, dispersal).

Tielbörger et al. use a massive series of carefully-controlled common garden experiments to reveal strong evidence for “bet-hedging” germination in annual plants. Roughly, bet-hedging is a way of maximizing your expected relative fitness in an uncertain environment. Germinating all your seeds every year (going “all in” in betting parlance) provides a big payoff if the year turns out to be a good one, but it is very risky. If the year turns out to be a bad one, all the resulting plants will die before reproducing (the ecological equivalent of “going bust”). But conversely, if you never germinate any seeds, so that your seeds just sit in the ground, they’ll eventually all die without reproducing (“nothing ventured, nothing gained”). So the optimal germination fraction (the one with the highest expected relative fitness compared to the others) will be some intermediate fraction, the precise value of which depends on the probability distribution of different kinds of years. That’s the theory, anyway. But strong empirical tests are almost non-existent, because they’re really difficult. For instance, you have to control for environmental and genotype x environment variation in germination fraction. The authors went to the trouble of developing inbred lines of each of three annual plant species, growing up their seeds in a common greenhouse environment to eliminate maternal effects, and then planting those seeds into common gardens along a rainfall predictability gradient in the field, and along an artificial rainfall gradient in the greenhouse. As expected, species subject to higher risk of reproductive failure exhibit lower genetically-determined germination fractions. Yes, Virginia, annual plants really do hedge their bets–and those that face more risk do more hedging!

Fraker and Lutbeg develop an individual-based model of mobile predators and prey and show how limitations to the movement rates and perception distances of individuals cause their spatial distributions to deviate from the ideal free distribution. If you have limited information (=limited perception distance) and limited ability to act on that information (=limited movement rate), you can’t attain the ideal free distribution (which assumes that you have perfect information which you’re free and fully able to act upon). Which at that level is kind of obvious, but Fraker and Lutbeg explore precisely how the resulting distributions deviate from ideal free, which is much less obvious. Bailey and McCauley (2009) is one nice experimental paper showing data illustrating some of the predicted consequences of limited information and movement rates. More broadly, I always like stuff that shows the complex and counterintuitive macroscale consequences of different microscale assumptions about the behavior and movement of individual organisms. Maybe if people write enough of these kinds of papers, other people will quit trying to infer the underlying microscale processes directly from inspection of (or some sort of randomization of) macroscale data.

Speaking of starting from microscale assumptions and deriving their macroscale consequences, Casas and McCauley ask: What’s the functional response of a predator that must divide its time between searching for prey, and other activities (broadly denoted as “handling”)? If you said “It’s an increasing saturating function and we’ve known that since Holling (1959),” you’re right–sort of. That is, you’re right only if you’re prepared to make radical simplifying assumptions about the relative timescales of the underlying processes that cause predator individuals to change “states” (here, from the state of “searching for prey” to the state of “handling captured prey” and back again). If you want to avoid such radical (and often unrealistic) assumptions, then you have to be prepared to do much more complicated math, which Casas and McCauley illustrate for both parasitoids and a predator (Mantis, the same predator considered by Holling himself in a classic 1966 study of predator functional responses). One consequence of increased realism is that the predator population never reaches an equilibrium or stationary distribution of individuals in different states, a fact which turns out to have important and testable consequences for predator-prey dynamics.

Finally, I don’t see how I can get away without mentioning Mata et al., an impressively large protist microcosm experiment manipulating disturbance intensity, disturbance frequency, nutrient enrichment, and propagule pressure in factorial fashion and examining their effects on resident community structure and invader success. As you’d expect, such a complicated experiment throws up complicated results, some of which seem to be readily interpretable (e.g., high disturbance intensity creates conditions that favor invaders with high intrinsic rates of increase), others less so. I do think it’s a little unfortunate that the authors frame their experiment as a test of Huston’s “dynamic equilibrium model”, since that “model” shares the same fatal logical flaws as zombie ideas about the intermediate disturbance hypothesis. I suggest that framing the experiment in terms of logically-valid theory might have aided interpretation, and possibly even suggested a somewhat different experimental design.

Many other interesting-looking papers coming out, but I don’t have time to dig into all of them so this’ll have to do for now. Happy reading!

*p.s. Just so you know, no one has ever told me, hinted to me, or implied to me that I should promote the journal’s content. When I highlight Oikos papers that I think are particularly interesting, it’s because I think they’re particularly interesting. It’s not like I ever think “Ok, gotta pick some Oikos papers to talk up now.” I hope you’ll take my word on that, given that I also link to a lot of non-Oikos content and criticize Oikos papers. Don’t get me wrong, I’m an Oikos editor and author, I like the journal, I want to see it do well and continue to fill what I think is an increasingly crucial niche, and I think the blog can help achieve that. And so when I do highlight interesting papers, I highlight interesting Oikos papers. But if I didn’t think there was anything worth highlighting, I wouldn’t. So I hope you find it valuable if I occasionally highlight Oikos papers I find particularly interesting, or invite the authors to do so, just like I hope you find the other posts valuable. But if for whatever reason you don’t, that’s fine.

Note as well that in saying this, I mean no criticism of any other journal blog, many of which focus much more than we do on the content of the associated journal. Different blogs are different.

Provocative new Oikos paper: should we reallocate funding away from the ecological 1%? (UPDATED)

My fellow Oikos editor and blogger Chris Lortie has a strong interest in scientific publication practices (see, e.g., here). His latest effort, now in press at Oikos, examines patterns of funding and impact among the ecological 1%: the most-cited 1% of ecologists over the last 20 years (Lortie et al. in press). Chris is too busy right now to blog it himself, so I’m going to do it, because I think it’s a must-read.

In a previous paper (UPDATE: link fixed), Chris and his colleagues reported detailed survey data characterizing 147 of the most-cited ecologists and environmental scientists. Not surprisingly, they are overwhelmingly male, middle-aged, employed in North America and Western Europe, have large, well-funded labs, publish frequently, and have high per-paper citation rates.* But there’s a surprising amount of variation (multiple orders of magnitude) in terms of lab size and funding level within this elite group. A feature of the data which Lortie et al. take advantage of to ask how citation rates vary with funding level within the elite.

In their previous work, Chris and his colleagues have shown that, for non-elite Canadian ecologists, more funding is associated with more “publication impact efficiency” (PIE): more highly-funded researchers also have more citations per dollar of funding. But Lortie et al. find that the same is not true of the elite. Using a slightly different measure of PIE (citations per publication per dollar), Lortie et al. find no relationship (not even a hint!) between PIE and funding within the ecological elite. Again, that’s despite multiple orders of magnitude of variation in funding level within the elite. Combined with their previous results, this indicates diminishing returns to really high funding levels (above several hundred thousand dollars, roughly). The implication is that funding agencies looking to maximize the “bang for their buck” arguably should reallocate funding away from really elite researchers and towards non-elite researchers. This wouldn’t reduce the PIE of the former group, but would increase the PIE of the latter group. Actually, Lortie et al. are careful to suggest increased funding for non-elite ecologists, rather than a reallocation of existing funding. But opportunity costs are ever-present so long as total funding is finite, and so I don’t think it’s possible to avoid the implication that these data suggest reallocation of funding away from the “elite of the elite”.

This is really thought-provoking stuff, and I hope that the folks who run our funding agencies take note.** One thing I’d like to see is for funding agencies to use this kind of information to give guidance to grant referees on how to evaluate applicants’ track records. For NSERC Disovery Grants, the “excellence of the researcher” (basically, the reviewers’ evaluation of your track record of publications and other outputs over the previous 6 years) is 1/3 of the grant score. To my knowledge, NSERC currently offers no guidance as to whether “excellence” should be scaled relative to the applicant’s funding level (which the applicant is obliged to report). These data suggest that it should be, and further that the appropriate scaling is nonlinear. Against that idea, one could note that increased funding gives researchers various advantages that let them increase their per-publication impact as well as their publication rate. So ultimately it’s impossible for reviewers (or anyone) to try to tease apart how much of an applicant’s track record is just due to their funding level (the idea being that anybody with lots of funding will have a good track record), and how much is due to their “intrinsic” excellence.

I am curious to see results for elite and non-elite researchers using exactly the same measure of PIE. Perhaps Chris can provide these numbers in the comments.

All of the usual caveats about citations as a measure of “impact” apply, obviously, and Lortie et al. recognize those caveats. But the conclusions here are, I think, robust to those caveats. Basically, there’s an upper limit to the mean quality of papers that any lab is capable of producing–and it turns out that even the most brilliant ecologist’s lab hits that limit at a funding level of several hundred thousand dollars or so.

One other caveat is that these are observational, comparative data. They aren’t necessarily a reliable guide to the effects of an “experimental manipulation” such as a reallocation of funding away from the elite. But they’re the only guide we have. Though having said that, I’d also be interested in analyses tracking changes over time in the funding level, PIE, and other relevant variables for individual researchers. Would it lead to the same conclusions?

In passing, one minor quibble I have is that Lortie et al. describe elite researchers as especially “collaborative”. But by this, they seem to mean simply that elite researchers have larger labs on average than non-elite researchers, not that they have more extensive collaborations with colleagues outside their labs. Which seems like a rather unconventional definition of “collaboration”.

There are analogies here to debates in economics over income and wealth inequality and their consequences, which are too obvious for me to ignore–but too incendiary for me to comment on!

This should be an interesting comment thread…

*Click through and read the whole thing for data on other characteristics of elite researchers–such as how hard they work and how much alcohol they drink!

**At least some of them are thinking about this stuff. I can’t find the citation, but a little while back NIH did analyses along these lines for their researchers, and discovered the same pattern of diminishing returns for really well-funded labs. Although the threshold funding level beyond which there was no further increase in efficiency was higher than in ecology, as you’d expect given the higher cost of much biomedical research.

Cool new Oikos papers

Some forthcoming Oikos papers that caught my eye:

Tuomisto (in press) is a “consumer’s guide” to evenness indices, showing how they are mathematically related to one another, and to partitionings of diversity into alpha and beta components. The take home message is the same as in my recent post: different “evenness” indices actually measure different things. To pick one, you need to know exactly what you’re trying to measure. And it is not interesting to simply ask whether different indices give you different results, because they will as a matter of mathematical necessity.

Ackerman et al. (in press) use a comparative approach to test the popular and intuitively-appealing hypothesis that pollinator extinctions and temporal fluctuations in pollinator abundance select for flowers attractive to many pollinator species. By combining long-term census data on 37 species of Panamanian euglossine bees with data on bee and flower phenologies, Ackerman et al. show that the “risk hedging” hypothesis doesn’t work. There’s no tendency for generalized plants to be pollinated by more variable pollinators. Rather, the longer a plant flowers, the more bee species visit it, which suggests that plant-pollinator specificity is just a sampling phenomenon (the longer you flower, the larger the “sample size” you’re taking from the pollinator fauna). As a contrarian, I always like to see widespread intuitions put to the test–especially when they’re found wanting.

New et al. (in press) develop a stochastic, mechanistic predator-prey model for the dynamics of hen harriers and red grouse, fit it to long-term time series data using state space methods, and use the fitted model to evaluate alternative management strategies for predator suppression. Red grouse is a popular game species in the UK, but you can’t hunt grouse that hen harriers have killed. It’s illegal to cull harriers, leading to the idea of “diversionary feeding”–give the harriers alternative food so they stop hunting grouse. Which sounds like a good idea until you realize that (i) it’s expensive, and (ii) in the long run, you might just build up higher harrier abundances, which would lead to even heavier predation on grouse than would otherwise occur (a specific example of the general principle of apparent competition; Holt 1977). The results show that harriers do suppress both average grouse density and grouse cycle amplitude (red grouse are a famous example of cyclic dynamics, driven by density-dependent parasitism). That’s a really cool result in and of itself. There aren’t many good examples of “community context” mediating the stability of population cycles.  The results also show that diversionary feeding, as currently practiced, makes only a marginal difference at best.

Numerous other forthcoming papers caught my eye–we’ve got a lot of good stuff coming out. But I need to get back to marking, so they’ll have to wait for a future post.

Cool new Oikos papers (UPDATED)

Lots of interesting papers coming out in Oikos in the next little while. I wanted to highlight a few that particularly caught my eye.

In the most recent (Feb. 2012) issue:

  • Barto & Rillig on dissemination biases in ecology. This is a really important study. Barto & Rillig analyze the citation rates of almost 4000 papers included in over 50 ecological meta-analyses. Studies that report unusually strong effects (compared to other studies on the same topic) tend to be published first, published in higher-impact journals, and get cited more frequently–even though they also have the smallest sample sizes and so are objectively provide the least reliable estimates of effect size and direction. The overall picture is that we suffer from confirmation bias and theory tenacity–we tend to cite the studies that appear to confirm what we (think we) know, and that appear to support existing theory. I suspect the bandwagon effect also contributes here; everybody tends to cite the stuff everybody else cites. Which is an especially serious problem when, because of confirmation bias, those studies are the least-reliable ones. You wonder how zombies first arise? This is how! (UPDATE: Check out Mike Fowler’s discussion of this paper, including his own personal run-in with an anonymous reviewer who seems to be guilty of the sins Barto & Rillig quantify)
  • Gotelli & Ulrich on null models. In an old post I argued that ecologists should refight the null model wars. I didn’t realize when I wrote that post that leading null model proponents Gotelli & Ulrich had already decided to fire the first shot! Although their title suggests a focus on purely statistical issues (such as testing for significant deviations from the null model), in fact the ms actually engages with deeper conceptual issues, such as how we figure out what our null expectation should be in the first place. I’ll try to do a longer post responding to Gotelli & Ulrich at some point, as I disagree with some of what they have to say. But it’s great that they’re bringing out into the open issues that were basically swept under the rug many years ago, and so aren’t familiar to many younger ecologists.
  • Valladeres et al. on how forest fragmentation leads to food web contraction. The authors compile a truly massive set of plant-herbivore and host-parasitoid food webs for 19 Argentinian forest fragments of varying area. Smaller fragments harbor a subset of the food webs in larger fragments, specifically the highly-connected “core” species. This is interesting for a couple of reasons. First, it shows that extinction risk isn’t just a matter of a species’ own “traits”, it’s also a matter of the food web context in which the species is embedded. The same species could be more-connected (relative to others in the web), or less-connected, depending on which other species happen to comprise the web. Second, the results may have implications for the links between community stability and “complexity”. If “complexity”, in the form of high connectance, is destabilizing, then you might expect food webs to collapse by losing highly-connected species, the opposite of what these authors found. However, even their most highly-connected webs were still pretty-low connectance in absolute terms. For that and other reasons the results are merely intriguingly suggestive in terms of their implications for complexity-stability theory.
  • Fox & Kerr on an extended Price equation partition. Yes, a shameless plug. In nature, species composition often exhibits turnover along environmental or spatial gradients. Ecosystem-level properties and “functions” also vary along those gradients. In this paper, Ben Kerr and I use Ben’s clever extension of the Price equation to partition between-site variation in ecosystem function into components attributable to different effects (e.g., changes in species richness vs. changes in species composition vs. environmental effects on the functioning of individual species). One interesting insight is that, when there is compositional turnover, there’s no single “species richness effect” and no single “species composition effect”. Rather, there are two of each. So all those arguments ecologists have had about how to separate “the” effect of species richness from “the” effect of species composition are badly framed.

We have many more interesting articles in the pipeline, so look for more “highlights” posts in the near future.

Interesting recent and forthcoming Oikos papers

The editor’s choice posts are Chris Lortie’s domain, but he’s very busy right now and so I thought I’d fill the gap by briefly highlighting a few recent and forthcoming Oikos papers that caught my eye.

The current issue of Oikos has lots of intriguing-looking stuff. In particular, I like Adams & Vellend’s model of how intraspecific genetic diversity and species diversity can be mutually-supporting. It partially comes down to whether the presence of more species, or more genotypes, creates an appropriately non-transitive competitive hierarchy among all genotypes of all competing species. This may well be a general principle. Some more system-specific features of the model also matter (it’s tailored to grass-clover competition).

In the same issue, Meier et al. have a neat study of how local mate competition selects against the sex-specific dispersal distances that are common in many species. They use both a conceptually-simple model, and a complex individual-based simulation to make their argument.

Song et al. (forthcoming) argue that the “Tangled Bank” hypothesis for the evolution of sexual reproduction (genetically-diverse offspring occupy different niches and so avoid competing with one another, thereby enhancing parental fitness) has been too quickly dismissed. There are close connections between this classic evolutionary idea (there’s a version of it in Darwin’s Origin) and recent ideas about the interplay of intraspecific genetic diversity and interspecific species diversity such as Adams & Vellend.

Schroder et al. (forthcoming) report replicated whole lake experiments, involving the imposition and subsequent removal of a perturbation, with novel effects on food web states. They find that perturbation generates neither an irreversible shift to an alternate stable state, nor a reversible shift. Rather, after removal of the perturbation the food web settles into a state distinct from either the pre-perturbation or perturbed state. This is a novel result as far as I know, and not a possibility that theory has much considered.

Finally, Barto & Rillig (forthcoming) report what looks to be a very important study of dissemination biases in ecology. Studies which report extreme effect sizes tend to be published first, and in in the highest-impact journals, independent of sample size. More worryingly, there’s a tendency for theory tenacity: studies that support our ideas are more heavily cited than those that don’t, again independent of sample size (=study reliability). Apparently, one reason zombie ideas are so hard to kill is that we don’t want them to die!

Oikos article blogged

Over at Distributed Ecology, Ted Hart has a nice discussion of Lima & Berryman’s recent Oikos article on positive and negative feedbacks in human population dynamics. The authors argue that the complexities of human behavior and societies create novel sources of negative and positive density dependence in human population dynamics, the strength of which has varied in human history, and also varies geographically. You should check them both out.

The art of hand waving

Hand waving‘ in science has a bad reputation; referring to an argument as ‘hand waving’ suggests a lack of rigor. But is hand waving always a bad thing?

If by hand waving we simply mean omitting assumptions or steps in an argument for no good reason (or worse, for a bad reason, such as the desire to mislead the audience), then yes, hand waving is bad. But there are often good reasons for such lack of rigor. For instance, presentational reasons: the time constraints of a seminar often oblige the speaker to gloss over technical details. More interestingly, there can be substantive reasons for hand waving (and the line between presentational and substantive hand waving isn’t clear cut). Ecology is hard, and hand waving makes it easier. In order to make progress, we are often faced with a choice, not between a rigorous argument and a hand waving argument, but between a hand waving argument and no argument at all. Hand waving can include heuristic arguments, approximations, and rough ‘back of the envelope’ calculations. I’d also include rigorous models of simple situations which can, via hand waving arguments, be used to develop hypotheses about, or interpret data from, more complex situations. The hope is that the simple model somehow ‘captures the essence’ of the complex situation. (What it means to ‘capture the essence’, and how it’s different from, say, ‘getting the right answer for the wrong reasons’, is a subject for another post…)

Indeed, since all models (mathematical and otherwise) have simplifying (i.e. false) assumptions, all models are in a sense hand waving arguments about what the real world might be like. Simplifying assumptions are a feature, not a bug, a point well-articulated by philosopher Bill Wimsatt and in an ecological context by Hal Caswell. A model with no simplifying assumptions would be like a map as big as the world itself, and equally useless.

Hand waving arguments are perhaps especially common in community ecology, where our theoretical models typically are much simpler than the natural communities to which they’re applied (although not inevitably so, as I’ve discussed in a previous post). At least, that’s the perception of community ecology; I wouldn’t venture to guess at how true the perception is, though I’m not above joking about it. My former colleague Ed McCauley and I used to joke that community ecology consists of theory on one side, data on the other, and a bunch of community ecologists in the middle frantically waving their arms (arm waving being a more extreme form of hand waving). In contrast, the best population ecology involves tight, rigorous connections between theory and data; population ecologists hold their arms stiff at their sides like Irish step dancers. This was certainly true in the case of Ed, one of the world’s best and most rigorous population ecologists. If Ed were stranded on a desert island, I doubt he’d wave his arms to attract a passing ship (which brings us back to the point that sometimes arm waving is a good thing, such as when the alternative is to be stranded).

Ed and I are of course not the only ones to get a chuckle out of hand waving:

(cartoon by Sydney Harris)

Of course, there are no hard and fast rules about what’s a good (or good-enough) approximation, or what’s an essential vs. inessential detail. So hand waving arguments always involve some judgment calls. There’s an art as well as a science to hand waving. But just because hand waving involves judgment calls doesn’t mean there aren’t better and worse hand waving arguments (much like there are better and worse judges). I think that some ecologists definitely are better at hand waving than others. Mathew Leibold and Jon Chase are great hand wavers. They’re really good at using simple, equilibrial food web models with just 2-4 species to think about complex phenomena like turnover in species richness and composition along natural environmental gradients. No, I’m not going to tell you who I think the bad hand wavers are…

(UPDATE: Jon responds by saying ‘Thanks…I think’. In case there was any doubt, I really do mean it as a complement when I call Mathew and Jon great hand wavers, although I suspect they may not think of themselves in that way.)

Oikos recently published a nice piece of handwaving from Graham Bell. Natural populations are always fluctuating in size, and we’d like to infer from the pattern of fluctuations something about the underlying ecological mechanisms driving them. Graham develops simple alternative models to predict the relationship between successive minimum population sizes (i.e. population sizes lower than any that came before), and the expected time before the next minimum occurs, and tests those models with data from a long-term marine plankton monitoring program. The data support a model in which population fluctuations are driven by trophic interactions, so that minimum abundance decreases exponentially over time. There’s hand waving going on at multiple levels here, not just in the development of the models (all except for the food web model are extremely simple, ‘capture the essence’-type models). What justifies the hand waving is that the answer that comes out is extremely clear cut. The whole point of a hand waving argument is to skim over inessential details, and one indication that you’ve done so successfully is by getting a clear cut answer at the end.

Feel free to recommend any really good (or really bad!) examples of hand waving ecology in the comments.

'Synthesizing ecology': revisiting an Oikos classic

Oikos’ motto is ‘Synthesizing ecology’. This has always struck me as an intriguing slogan, because it can be read in multiple ways. It might be thought to highlight our desire for generality. As our instructions to authors note, Oikos strives to publish papers with broad implications, which will therefore be of interest to many ecologists. On this reading, ‘synthesizing’ is synonymous with ‘generalizing’. For instance, Persson et al. (Oikos 119:741-51 [2010]) pull together (‘synthesize’) data on stoichiometric homeostasis for many different species, thereby allowing them to reach the general conclusion that all heterotrophs exhibit stoichiometric homeostasis.

But a second, related but distinct reading is possible. ‘Synthesizing’ can refer to combining different parts or ingredients into a new, unified whole, as when chemists synthesize a new compound. Indeed, this is the dictionary definition of ‘synthesizing’. Synthesizing in this sense is a teleological (goal-directed) activity—one must ‘decide’ (consciously or otherwise) what ‘whole’ one wants to make, what ingredients to use, and how to combine them. These decisions are constrained. Choosing what one wants to make constrains one’s choice of ingredients and ways of combining them. And choosing ingredients and ways of combining them constrains what one can make.

Ecological generalizations are ‘synthetic’ in this second sense. Ecologists choose what questions to ask—we choose what ‘wholes’ we want to make. After all, ecological systems—organisms, populations, communities, ecosystems—have an infinity of properties one might measure, and so there is an infinity of questions we might ask. Only once we’ve chosen the question does nature answer it. And the way in which we frame our questions shapes what ‘ingredients’ we can use (e.g., what sorts of data we need), and what sort of answers we get.

This second sense of ‘synthesis’ grounds my own response to John Lawton’s ‘Are there general laws in ecology?’ (Oikos 84:177-92 [1999]). It’s a classic Oikos article—cited 399 times to date, and the annual citation rate has hardly declined over time. In it, John provocatively suggests that the answer to the question posed by his title is ‘scale dependent’. There are (contingent) generalizations at the ‘small’ scale of population ecology. For instance, there are millions of species, but only a few distinct kinds of population dynamics, and only a few key factors (e.g., intrinsic rate of increase, strength of density dependence) that govern what kinds of dynamics occur. There are also generalizations at the ‘large’ scale of macroecology, where the ‘noise’ of species- and system-specific details ‘averages out’. General macroecological patterns include power law species-area curves and lognormal species-abundance distributions. But at the ‘intermediate’ scale of community ecology, the contingency is overwhelming and there are no generalities—every community is a special case. The contingency is overwhelming because (unlike population ecology) there are too many relevant causal factors, and because (unlike macroecology) communities are too small-scale for these contingent details to average out. Provocatively, John (a community ecologist himself) says that traditional community ecology is a questionable use of ecologists’ time and effort, and ecologists ought to ‘move on’!

As a community ecologist myself, I can certainly see where John’s coming from; his argument absolutely deserves the widespread attention it has received. Part of my own answer to his argument is to sidestep it by saying that general patterns are important, but describing and explaining them isn’t the only way to do good ecology. (Peter Kareiva articulates this view in a fine essay for NCEAS, still available here in a forgotten backwater on one of NCEAS’ servers) But my main answer is to suggest that the apparent overwhelming contingency of community ecology, and the apparent (relative) simplicity of population ecology and macroecology, isn’t some brute fact of nature. It’s our own creation. It reflects the questions we’ve chosen to ask—the syntheses we’ve tried to make, and the ingredients out of which we’ve tried to make them.

Anything in nature can be described in more or less general terms. I’m a human being, but I’m also a mammal, a vertebrate, an animal, a living organism, and a chunk of matter (and a lot of other things too!) The level of generality with which we frame our questions is our choice. Key questions in population ecology often have been framed at a very high level of generality—for instance, whether per-capita growth rates generally are density-dependent or not. Without this highly-general framing, population ecology would appear just as complex as community ecology. What if, instead of asking questions about density-dependence, we instead chose to ask questions about the relative importance of all the many different sources of density-dependence—predators, parasitoids, pathogens, intraspecific competition, indirect effects, maternal effects, etc., plus all possible combinations of these? Population ecology would suddenly appear to be an overwhelmingly complicated collection of special cases. Not that we couldn’t make it even more complex than that, if we so chose (what about subcategories, such as competition for food vs. for territories vs. for mates?). The same goes for macroecology, where debate often centers on whether we should focus on general trends, or on the variation around them. From the latter point of view, the general trends are trivial statistical epiphenomena, created by averaging away interesting variation among different special cases.

So if the questions we often ask in community ecology have highly contingent answers, maybe we should ask more general questions. For instance, are community dynamics generally characterized by negative frequency dependence—i.e. do species that become sufficiently rare (relative to the others) tend to bounce back? That’s a very important question; it basically amounts to asking if species are stably coexisting or not. The answer has immediate implications for a large body of mathematical theory, and for the practical conservation of biodiversity. That question also is quite closely related to the population ecologist’s question about density-dependence, since density-dependence at the single-species level is manifested as negative frequency dependence at the community level. Now, there are of course many different underlying mechanisms that can give rise to negative frequency dependence. But the fact that all those mechanisms generate frequency dependence is a key general feature they all share, so why not start by focusing on that general feature? And then follow up by asking only slightly more detailed questions, such as whether negative frequency dependence arises primarily from variation-independent mechanisms (i.e., mechanisms that could operate even in a homogeneous, equilibrial world) or variation-dependent mechanisms (i.e. mechanisms that only operate in a spatially- and temporally-variable world)? These questions aren’t hypothetical, nor are they my idea. For instance, Peter Chesson’s theoretical work has long been addressing such questions (Chesson 2000 Ann. Rev. Ecol. Syst. 31:343-66), and field ecologists are now doing so as well (e.g., Adler et al. 2006 PNAS 103:12,793-8). One strand of my own work (shameless plug alert!) tries to develop general theoretical frameworks that would let us ask such general questions in areas where we can’t currently do so (e.g., Fox 2010 Oikos 119:1823-33).

My point is not to criticize the level of generality at which John, and many of my fellow community ecologists, ask community ecology questions. More and less general descriptions of nature complement one another, and a strong science needs both. As John points out, if we only ask detailed questions, the answers we get will tend to look like a stamp collection. But conversely, if we only ask very general questions, we are likely to get only general, imprecise answers, or perhaps even no answers at all (many of the macroecological patterns John cites are infamous for ecologists’ inability to agree on their causes). But if we ask both more and less general questions, the more general ones provide a framework with which to organize the answers to the less general ones. At the same time, the less-general questions provide precision we would otherwise lack. Evolutionary biology is a good example of a field which draws strength from asking both sorts of questions. Without the general theory of evolution by natural selection, studies of, say, changes over time in the bill sizes of Darwin’s finches and in bacterial antibiotic resistance would not have any apparent connection at all, never mind be recognized as two classic examples of natural selection in action. But without detailed studies of specific cases, we could make no quantitative statements about, e.g., how strong selection typically is. We would be limited to making axiomatic statements about evolution, such as Fisher’s Fundamental Theorem.

It’s ecologists who ‘synthesize’ ecology. If we are clever enough, we can get nature to answer any question we ask. So if we don’t like the answers we’re getting, it’s up to us to ask different questions. I look forward to seeing what sort of ecology Oikos authors will create in the future.